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Anticorruption Enforcement and Sale Mechanism Choice in China’s Land Market
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Keywords\textemdash Chinese real estate, causal inference, marginal structural model, land allocation, auction design
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In the years leading up to the liquidation of Evergrande\textemdash formerly China's largest real estate developer and one of the largest companies in the world\textemdash the Chinese real estate market was growing rapidly, with housing prices increasing exponentially since 2000 (zhao_playing_2017). Underlying this growth lay a distinctive incentive structure: local governments relied heavily on land sale revenue to fill fiscal deficits and were thus incentivized to raise the standing and attractiveness of their locality. This often involved strategic management of the land supply. For instance, local governments would sometimes sell industrial land for low prices in order to attract desirable industries to the area, but residential land was more tightly controlled to drive up the land's selling price and value. In this market characterized by such rapid price appreciation, any discount could yield a significant profit for developers\textemdash and in these circumstances, corruption naturally found a foothold.
Ultimately, by 2012, corruption had become endemic to the Chinese land sale market, effectively shaping every aspect of land development\textemdash how much land was sold, in what way, to whom, when, and at what price. In this environment, shortly after taking control of the Party in late 2012, President Xi launched a broad-sweeping, top-down anticorruption campaign that investigated officials at every level of government. The campaign took the form of anticorruption waves: teams of investigators were dispatched to a set of provinces and conducted investigations into corruption for a few months, returning to Beijing afterwards to report findings. Under political pressure from the central government, local governments were then empowered to prosecute offenders and deter further corruption. This centralized and extensive anticorruption campaign provides an interesting setting to directly investigate corruption's impacts in the land market, and this paper focuses on one pathway in particular\textemdash corruption's impact on the sale method used by a local government when selling a property, and subsequently, how corruption influences the sale price faced by developers. In essence, one sale method (the listing) is believed to be associated with corruption in the literature.
To investigate this relationship, I utilize a dataset on corruption indictments reported at the prefecture level, as well as comprehensive land transaction records scraped from the Chinese government's land transaction database. After performing a two-way fixed effects specification and finding the assumptions are not met, I use a marginal structural model (MSM) with unit-level fixed effects in the inverse probability of treatment weighting (IPTW) model, which is used to create the weights for each unit. MSMs are an underutilized inference tool in the social sciences, particularly given the shortcomings of traditional two-way fixed effects specifications, as described in imai_use_2021. Developed by Blackwell and Yamauchi (2021, 2024), the MSM with fixed effects in the IPTW is a novel tool to bypass the traditional shortcomings of MSMs, and this paper is the first to apply the Blackwell and Yamauchi methodology. Further, the question at the heart of this paper\textemdash corruption's impact on the sale method and sale price of land, as reflected by the anticorruption campaign\textemdash has not yet been examined in the literature. This paper also makes important contributions on the data side with its new, accurate data set\textemdash an important development given that a dominant data set in the Chinese real estate space (chen_busting_2019) was revealed to have significant accuracy issues.\footnote{See manso_are_2026 for a discussion of the data problems of chen_busting_2019.}
In this analysis, corruption investigations serve as the treatment, and the sale method is the outcome. I ultimately find a statistically significant negative effect when prefecture-level fixed effects are included in the IPTW model: using marginal effects, a prefecture having corruption indictments causes a 1.16 percentage point decrease in the probability of having any listings. However, this effect is further compounded when sequential periods are treated, and additionally, uncertainty in the timing of the indictment means that the effect on the outcome may also spill into neighboring time periods. Investigating the cumulative effect for the five-month period around having a corruption indictment reveals a 7.78 percentage point decline in the probability of having any listings. Sensitivity checks are conducted on these results and evaluate whether the assumptions are satisfied, finding that any violation of the assumptions would likely cause the coefficients to be underestimates.
This paper then examines the relationship between sale method and price via an additional MSM and finds that the mean and median land sale price rise in the presence of corruption indictments. Specifically, a prefecture having corruption indictments in a given month/year causes, on average, a 6.78% increase in the mean price per square meter, and the median increases similarly. Given that the mean is 2,200 yuan per square meter (US\$350) and that properties tend to be tens of thousands of square meters, if not more, a nearly 7% increase represents a significant amount of cash. Interpreting these results together, I posit that the anticorruption campaign does deter actual corrupt behavior (i.e., having listings on favorable properties), but that it also impacts behavior for properties on the margin (i.e., those that could be sold as either auctions or listings).
This paper is structured as follows. After offering background on the land sale process and President Xi's anticorruption campaign (Section (ref)), Section (ref) offers a literature review. Section (ref) gives an overview of the data and its collection/cleaning process. Section (ref) briefly discusses the two-way fixed effects specification and why it falls short in this context before outlining the MSM with fixed effects. Section (ref) details the results, and Section (ref) examines the relationship between corruption indictments and price to offer insight into how market behavior changes in the presence of the anticorruption campaign. Section (ref) concludes.
First, to understand how the Chinese land finance system operates, I provide background on China's land use system and land auction system, discussing why corruption is so attractive and prevalent in the land use environment. I then introduce Xi's anticorruption campaign and its effects.
Under the Chinese system, the government is the ultimate owner of land, and funding from land use right sales (dubbed “land finance") is a critical part of local governments' funding. The system is incredibly complex and multifaceted, but in essence, the local government creates new urban land use rights (LURs) via land acquisition and subsequently sells these LURs to private and public land users (gyourko_land_2022).\footnote{In China, all urban land is owned by the State while rural and suburban land can be owned by rural collectives (“collective land") (huang_land_2018). Thus, when a local government purchases new land, it is either purchasing rural land from one of these collectives or buying back the land it previously sold\textemdash that is, reacquiring LURs for land already developed (gyourko_land_2022; zhang_china_2015). Because the government is the sole party able to purchase land (having eliminated the secondary market for LURs in 2004) and has strict rules about how land prices can be calculated, the State is able to purchase land from collectives and from current LUR holders at prices advantageous to itself (li_urban_2019; gyourko_land_2022). Thus, when a local government sells a LUR, it is selling the right to use the land for a fixed period\textemdash for instance, 70 years for residential, 40 years for commercial, and 50 years for industrial, although these may be shorter depending on the municipality\textemdash but it is still the ultimate land owner (su_visible_2012).} When a local government sells a LUR, it receives an upfront, lump sum payment from the developer, and the difference between the purchase and sale price is the local government's profit, which it then uses to finance other aspects of its budget (wang_political_2016).
Every 15 years, the State releases the national-level “Land Use Master Plan," which effectively caps the amount of rural-to-urban land conversions during the specified 15-year period in each province. The provincial government then issues quotas to each city, which are subsequently passed down to lower levels of government (gyourko_land_2022). Every year, each local government (specifically the local land resource bureau) creates a “Land Use Annual Plan," setting its expected rural-to-urban land conversion and urban land supply for the year. It is this plan that includes the list of the land parcels that the State will auction that year (wu_primary_2020).\footnote{There are also pathways for local governments to raise the quota, for instance, by trading quotas with other local governments or negotiating with higher-level (provincial) governments. Local governments could also disregard the quotas and accept punishments, which are relatively minor if certain requirements are also met (gyourko_land_2022). } Then, an independent committee of the city's political leaders and key figures from government agencies, such as the land resource bureau and the urban planning bureau, decide key constraints for each property to be sold, and when the land comes up for sale later during the year, they determine sale price as well (cai_build_2017; cai_chinas_2013). Responsibility for the land is finally passed to the local land bureau, which executes the land sale and decides the auction style (cai_chinas_2013).
The local government subsequently decides the timeline of LUR sales for the year and each parcel's auction method. After land sale reforms implemented in September 2004, “leaseholds are, in principle, all sold at public auction," and there are three main types of auctions used in China: an English auction ($Paimai$, in Chinese), which is a standard ascending auction; a listing/two-stage auction ($Guapai$), an ascending open-bid auction in two related stages that last for a period of time; and a sealed-bid auction/tendering ($Zhaobiao$), where bidding is granted through invitation (cai_chinas_2013, p. 2; liao_boundedly_2023; zhu_shadow_2012). About 97% of LUR sales in major cities are comprised of English and listing auctions, with tenders (sealed-bid auctions) occurring only in Beijing and Shanghai for selected transactions.
A standard auction wherein the bidder who offers the highest price wins, the English auction is usually announced 20 working days in advance, at which time basic details like a property's use restrictions, reserve price, and location are released (cai_chinas_2013). Interested parties can also obtain additional information for a small fee and/or inspect the site itself. Participation in the auction then requires a cash deposit of around 10% of the reserve price, and the auction itself is often public, videotaped with press in attendance (cai_chinas_2013). Announced 20 working days in advance, listings are also known as “two-stage" auctions because of their format: the first stage typically lasts 10 working days after the auction begins, although it can last much longer in certain cases, and during this time, qualified bidders submit a bid (at or above the reserve price) in person or online. Bids are posted as they are made on the “trading board of the land bureau, as well as typically on the internet, although the identity of bidders is not posted" (cai_chinas_2013, p. 6; wu_primary_2020). Bidders can bid incrementally as many times as they want, and if there is only one active bidder at the end of the first stage, the land is sold to that bidder at their final bidding price (wu_primary_2020). If, however, more than one bidder was active at the end of the first stage, all active bidders enter the second stage\textemdash an English auction.
Finally, tendering/sealed-bid auction involves more complex criteria: the bid evaluation committee rates each bid on several factors, including not only the price of the bid itself, but also the credibility of the bidder, how much “social responsibility" the bidder is willing to take on, and the proposed development plan (cai_chinas_2013, p. 5; wu_primary_2020).\footnote{As described by cai_chinas_2013, credibility focuses on “the quality and reputation of the projects the bidder has developed in the past," in addition to the bidder's financial capacity (p. 5). “Social responsibility" is rooted in attempts to curb housing prices, for instance: developers who commit to upper bounds on housing prices receive greater scores.} As highlighted, these auctions are relatively rare, comprising only 2.69% of LUR sales between 2000-2015, according to data from the China Real Estate Index System (wu_primary_2020).
In addition to deciding which auction type to use, the local government determines all details about which way each parcel of land will be auctioned off, selecting the auction date and time, auction format, bidder qualification, and reserve price\textemdash and it is this latitude that allows corruption and under-the-table deals to occur.
Corruption in the land market is vast and complex, rising from a multitude of incentive structures and pathways. I detail only the theoretical pathway of corruption's influence on sale method here; others are explored in Appendix (ref). In effect, auctions are not fully “open to competition" because local governments decide all facets of the auction (zhu_shadow_2012). The key manipulation tools include raising the bar of entry into an auction, for instance, by requiring a minimum level of capital or certain ratings; merging small land parcels into one large parcel so that only the wealthiest firm can bid, and offering deals to provide infrastructure for new properties. The local government may also instruct firms to make deals amongst themselves before bidding for a plot opens (zhu_shadow_2012). Listings (“two-stage" auctions) are particularly susceptible to corruption. For instance, although the auction is announced roughly 20 working days in advance, the exact start date of the first stage is often announced at a much later date. Additionally, any firm wanting to bid in the first stage has to submit a bidding application and other basic materials, and local officials subsequently review the bidder's development qualifications and “integrity records"
In cases of corruption, those who “fail to meet the criteria" can be denied outright, or approvals to bid can be “delayed" until the first stage is already underway, excluding would-be bidders (cai_chinas_2013).
Indeed, cai_chinas_2013 investigated data from land sales in 15 cities across China from 2003-2007 and found that officials divert “hot" properties to the more corruptible “two-stage" auction, with many of these auctions often having only one bidder (and thus no competition). They further find that English auctions have competition and tend to result in higher prices, controlling for differential property characteristics such as distance from the business district. This result indeed makes sense given that English auctions are required to have a minimum of three “qualified bidders" (wang_are_2017, p. 199).\footnote{While some papers such as wang_are_2017 use the three “qualified bidders" requirement as reflecting a completely fair auction, I expect this requirement is not enough to wholly signal competition because developers can enter the auction with their different subsidiaries. That is, if China Vanke is the listed developer, two if its subsidiaries, Nanjing Yuyue Real Estate and Nanjing Yuxiao Real Estate, could enter the auction, comprising two of the three bidders, but they fundamentally represent the same developer (noauthor_2023_2024). This behavior became particularly rife in later periods, such as when the central government mandated mass land auctions in 2021: some of these auctions had over 300 entities participating\textemdash which actually represented only 30 developers (yu_chinese_2021). Nevertheless, cai_chinas_2013 find evidence that sale prices tend to be higher for English auctions than two-stage ones, suggesting higher levels of competition.} Figure (ref) below highlights this timeline and where corruption can interfere.
Note, however, as detailed fully in Appendix (ref), “even though [local governments] had been directed by the central government to increase land supply and cap home prices to keep a lid on social discontent" (shao_beijing_2013), they also had an incentive to raise revenue as much as possible, and LUR sales are an important source of this revenue. Additionally, prior to the anticorruption campaign, leading local officials' promotions could even be tied to Gross Regional Product (GRP) increases.\footnote{To curb this behavior, the government announced in late June 2013 that it will stop evaluating party officials solely based on their contributions to growing GRP, aiming to diminish the role of land sales funding local governments' budgets and reduce overinvestment in the sector (zhu_president_2013; guilford_china_2013).} Intuitively, this could lend itself to higher land prices, as officials would want to sell fewer properties for very high prices to maximize revenue (li_political_2005). However, viewing this from a utility maximization perspective provides insight: firms are simple profit maximizers, wanting to acquire land at the lowest cost, build as much as possible and as quickly as possible on that land, and sell units for as much as possible. Along the way, they are happy to spend money to “grease the wheels" (i.e., bribe officials) as long as it results in a higher revenue for the project. Officials are utility maximizers: those who get more utility out of bribes accept them, while those who do not abstain. The profits from corrupt sales, even if they are lower than they could be under greater levels of competition, often still allow the government to profit from the LUR sale\textemdash and this money is then funneled into infrastructure investment, which creates further demand for property in the region, allows governments to set higher reserve prices, and increases access to borrowing. This cycle continually repeats such that both officials and developers get what they want at every level. Officials can curry both political favor and profit at the same time by behaving as clever utility maximizers.
Interesting questions result when these motivations clash: for instance, when an official's boss seeks to follow the central government directive to limit land sale price growth and instructs the official to ensure no discounted land sales occur, but the official is offered a tempting bribe. Alternatively, when fear of detection rises, as in an anticorruption drive, the official may be tempted to bring job security into the calculation. This is the central question of this paper\textemdash is there evidence of the theoretical pathway between corruption and sale method, which in turn impacts sale price?
Prior to President Xi's top-down anticorruption campaign, anticorruption campaigns in China had been largely performative and had little impact on underlying corruption levels.\footnote{See Appendix (ref) for further details.} Xi's campaign, beginning in November 2012 and gaining steam in early 2013, launched what many consider to be the most intensive and protracted anticorruption campaign in the history of the People's Republic of China, catalyzing a period of reckoning and corruption indictments\textemdash and then, towards the end of 2016, the beginning of the transformation of the anticorruption infrastructure itself (wedeman_four_2016; deng_national_2018).
In the first months of 2013, Xi began preparing the anticorruption machinery before overseeing the creation of online reporting platforms wherein citizens could participate in supervision and reporting
Then, in mid-May, Xi dispatched 10 Central Inspection teams to a set of 6 provinces (Inner Mongolia, Chongqing, Guizhou, Hubei, Jiangxi, and Beijing) and 4 organizations (China Publishing Group, the Ministry of Grain Reserves and Water, the Export-Import Bank of China, and Renmin University of China, located in Beijing). These Central Inspection teams had until the end of July or early August to investigate their region/organization before reporting their findings to the inspected areas and the units of inspection (wang_76_2013). The Central Inspection teams then returned to Beijing to report their findings to party leadership\textemdash which includes all the parties and government members of the inspected areas (wang_76_2013). Findings, as presented in these meetings, held nothing back, often offering up scathing critiques of provincial problems, reporting everything from “abuse [of] power for personal gain," to corrupt hiring practices, to “inadequate management and supervision of top leaders, $\dots$ shaken beliefs, ideological decline, and moral deviance" (wang_76_2013, trans.).
As they progressed with further rounds of inspections, the Central Inspection teams sought to be nimble and unpredictable\textemdash one deputy director focusing on anticorruption remarked that if there was any kind of pattern or cycle to the anticorruption campaign, the officials under inspection would detect it and change their behavior, instigating “`falsification and cover-up'" (qtd. in wang_76_2013, trans.). The Central Inspection teams thus had revolving leaders and targets on their quest as they were dispatched to different provinces in several waves. Further, the Central Inspection team assigned to a province would not notify the region/units to be inspected until 10 days in advance, in writing, of their arrival, among several other measures to involve the public in reporting and enforcement. This nuanced and carefully planned workflow, designed to ascertain the true state of corruption in each area/unit as much as possible, was the blueprint for subsequent waves of the anticorruption campaign.
In this second wave, 10 Central Inspection teams were sent to 6 provinces (Shanxi, Jilin, Yunnan, Anhui, Hunan, Guangdong) and 4 organizations (Xinhua News Agency, Ministry of Land and Resources, Ministry of Commerce, and the State-owned company overseeing the construction of Hubei province's Three Gorges Dam).
The third round of central inspections began in late February/early March 2014 with officials being dispatched to 10 provinces (Beijing, Tianjin, Liaoning, Fujian, Shandong, Henan, Hainan, Gansu, Ningxia, and Xinjiang/Xinjiang Production Corps) and 3 organizations (the Ministry of Science and Technology, State-owned food processing company COFCO, and Shanghai's Fudan University)
In total, there were 10 anticorruption waves before August 2016, but for brevity, only those most relevant are discussed above.
This section offers a broader overview of the literature on corruption's impacts before moving into a review of studies on the impact of President Xi's anticorruption campaign.
Broadly defined as dishonest or fraudulent conduct by those in power, corruption has been extensively studied in the economic and statistical literature, particularly with investigations into its impact and mechanisms. Early studies such as becker_law_1974 and rose-ackerman_corruption_1978 focus chiefly on the relationship between the top level of government (principals) and officials (agents) who accept bribes. shleifer_corruption_1993 develop a theoretical framework to understand how corruption distorts government policies and outcomes, distinguishing two types of corruption: with and without theft. They describe the low-competition, low-detection settings that breed corruption, positing that a weak, decentralized central government allows multiple officials across government agencies to simultaneously collect bribes from the same private agent. They argue that corruption will not be deterred until its incentive structure and/or operational mechanism are overhauled, for instance, by implementing intragovernmental competition (i.e., making several agencies compete over the provision of a good).
On the heels of these early analyses, several studies began to quantify the empirical impacts of corruption, particularly focusing on the relationship between corruption, investment, and government income. Many of these studies have yielded diverging results based on the data, design, and statistical methods used: in one of the first and most prominent studies, mauro_corruption_1995, for instance, examines the impact of corruption on private investment, using an index of ethnolinguistic fractionalization as an instrument and finding that corruption lowers economic growth.\footnote{As described by mauro_corruption_1995, ethnolinguistic fractionalization (ELF) “measures the probability that two persons drawn at random from a country's population will not belong to the same ethnolinguistic group" (p. 682-3). Subsequently, many have critiqued this instrument for failing to meet exclusion restrictions: bentzen_how_2012 argues that based on the findings of acemoglu_unbundling_2005, ELF is likely correlated with other determinants of growth excluded from Mauro's analysis. Bentzen introduces a modified statistical approach and finds a similar negative effect of corruption on investment.} On the other hand, meon_is_2010 find that corruption can actually increase efficiency in highly inefficient regimes, and pradhan_impact_1999 emphasize that high levels of predictable corruption do not necessarily hinder economic growth.
Similarly, tanzi_corruption_1997 find that higher corruption is associated with higher public investment and lower government expenditure while poveda_relations_2019 find that higher corruption is associated with lower public investment and government expenditure. These results converge towards two alternate ideas/hypotheses: that corruption “greases" the wheels of bureaucracy, by allowing inefficiencies to be overcome with a private exchange, or “sands" the wheels, being harmful to economic growth and investment (meon_is_2010).
The overall consensus, though, is that corruption is generally associated with lower levels of economic growth and that whether or not net public investment and government spending increase with higher levels of corruption, these expenditures are less efficient and may be misdirected, tending to reduce productivity (mauro_corruption_1995; bentzen_how_2012; tanzi_corruption_1997; poveda_relations_2019; pradhan_impact_1999; meon_is_2010; meon_does_2005; and aldieri_corruption_2023, among others).
There is markedly less literature that analyzes the impacts of anticorruption campaigns, partly because national, top-down, sustained anticorruption investigations are quite rare. While there have been prominent anticorruption campaigns in South Korea (min_impact_2023), Brazil (castro_contextual_2017), Indonesia (widojoko_indonesias_2017), and India (riley_corruption_2016), among other countries, in recent years, the degree of efficacy has widely varied, and for the most part, detailed information on corruption indictments is not widely available. Yet, as explored in Section (ref), the case of China is an exception; a number of studies have emerged to investigate the extent of corruption and the impacts of Xi's anticorruption campaign.
The Chinese corruption literature has converged into a few strands. First, that highlighting the positive impacts of anticorruption: areas with stronger anticorruption efforts saw improved attitudes towards government credibility (zhang_anti-corruption_2019), improved acquisition of research and development (R&D) funding (xu_how_2017), reductions in stock price crashes (chen_does_2018), and increased entry of new firms (ding_equilibrium_2020). Other studies find the effects are more moderate and depend heavily on the level and number of officials arrested: kim_value_2018, for instance, analyze stock market price responses of all firms listed on the Shenzhen and Shanghai stock exchanges, finding that the market reaction to the campaign is “more positive for provinces where more department-level officials are arrested" but is negligible for the indictments of lower-ranking officials (p. 116).
Another strand focuses on how benefits of the anticorruption campaign diverge by firm ownership status, with kong_effects_2017 detecting differing firm performance trends based on whether a firm is a state-owned enterprise (SOE). Specifically, they find that the anticorruption campaign greatly improves performance for SOEs but significantly reduces it for non-SOEs. tian_how_2018 investigate how anticorruption measures affect corporate governance, finding that the reduction in executive incentives accompanying the anticorruption campaign was stronger for SOEs than non-SOEs. This evidence, they argue, suggests SOEs have been larger targets of Xi's campaign than non-SOEs. On the other hand, zhang_public_2018 finds that the anticorruption campaign and its new mechanisms have a greater impact on listed non-SOEs than SOEs, implying private firms are more sensitive to the campaign. zhang_public_2018 further notes that the campaign has a larger impact on firms in poor areas and areas with weak legal environments. cao_anti-corruption_2018 examine how corruption investigations shape firm information release. They note that regions with higher scrutiny experienced significantly lower negative information release in comparison to firms in other regions, finding a more pronounced effect for SOEs\textemdash who presumably have stronger ties to local authorities\textemdash compared to non-SOEs. Finally, alonso_value_2022 find that political connections have increased in importance for non-SOEs in the wake of the anticorruption campaign, as they help these firms receive more governmental subsidies. Comparatively, politically-connected SOEs still experienced “access to lower cost of debt, [but] at a lower magnitude than before" the anticorruption campaign (p. 785).\footnote{A smaller subset of analyses distinguish among the impacts of SOE status for “event firms"\textemdash those implicated in corruption investigations/scandals\textemdash and “non-event firms" who were not implicated (e.g., pan_political_2020, griffin_is_2022, and he_political_2017). The exact impacts of Xi's anticorruption campaign on SOEs vs. non-SOEs are complex, involve many different pathways, and are difficult to quantify, but the consensus is that the effect differs across both firm types and their event status.}
Other relevant papers investigating anticorruption in China include zhao_impact_2020, which uses a difference-in-differences design to identify the effects of the anticorruption campaign on land supply in China. They specifically focus on corruption of top leaders (mayors and Party secretaries) in prefecture-level cities, examining a date range of 2006-2016. They find that following the indictment of a major official for corruption, not only would the total amount of land supply drop sharply, but the proportion of profitable commercial and residential use land would decrease while that of public use land increased\textemdash in essence, the type of land supplied changed.\footnote{One recent paper by arslan_auctions_2025 compares listings and tenders in the Chinese market in the context of corruption. While the paper seems quite relevant, it utilizes chen_busting_2019's data\textemdash which suffers from a significant number of erroneous duplicates and a mistransformed measure of area, as highlighted in manso_are_2026. I thus do not give weight to its conclusions.}
Therefore, while these papers shed light on the impacts of corruption and the anticorruption campaign itself, my paper moves beyond the focus and methods of previous studies, not only investigating how the anticorruption campaign shapes the sale method, but making important contributions on the data side\textemdash a particularly relevant development given the prevalence of chen_busting_2019's faulty data in the literature.
I amalgamate data from multiple sources to investigate these questions. First, the data for corruption investigations was extracted from Tencent, the largest internet/multimedia company in China, by wang_how_2020. During Xi's anticorruption campaign, Tencent “launched a searchable online database of all corruption investigations across China since 2011" (p. 13). Combining and synthesizing information from “Party disciplinary committees, courts, and procuratorates from the central to local levels" (p. 13), this Tencent database is the most comprehensive publicly accessible repository of China's corruption investigations. Further, this database was provided for users to explore the extent of corruption in their town and province; as highlighted by Wang and Dickson, it is the “only place where Chinese citizens can find out this information with a single click" (p. 14) and has been widely circulated via Tencent's messaging app WeChat.\footnote{WeChat is China's most popular social media/messaging app, surpassing 1 billion users in 2018 (noauthor_one_2018).}
The data was scraped by Wang and Dickson in August 2016 via Python and contains detailed information on official indictments, including each official's name, position, locality, province, and the reason for investigation, as well as the official's rank of importance on a scale from 1-10. This scale defines 1 as state-level officials while 10 is deputy directors and below. On this scale, rank 3 is provincial governors and top officials in the party committee of each province. Rank 4 is mayors of major cities, vice governors, and lesser officials in the province-level party committee, among others of similar positions. A full description of the remaining ranks 5-10 is listed in Table (ref).
Entries also contain information on when the investigation into each official began, although approximately 1,600 out of 19,000 entries lacked the specific date of investigation (for instance, missing a month and/or year); the vast majority of these were officials of the lowest importance (levels 9 and 10 on the 1-10 scale). Where possible, I conducted additional research to fill in missing date entries, utilizing party newspapers and media to discern the dates that investigation into each official began. With this cleaning, I was able to complete over 1/3 of the incomplete entries, bringing the total number of entries missing the year and month of investigation to 933, and those missing only the month to 1,099. The relative counts of each rank of official, as well as their description, for the completed entries are included in Table (ref).
I obtain transaction-level data from the Ministry of Land and Resources' Land Transaction Monitoring System (\href{http://www.landchina.com/}{www.landchina.com}). As each municipality's “bureau of land and resources is required to report each land transaction in their jurisdiction electronically on this website," per the Law of Land Management (chen_busting_2019, p. 199), the dataset captures granular sale details for all land transactions. I focus on residential real estate land transactions for the years 2010-2017 that were sold via auction and listing, obtaining 209,706 total transactions.\footnote{A description of data cleaning procedures for the scraped data can be found in Appendix (ref).}
Control data comes from several sources: demographic and geographic coordinate information is derived from dong_census_2022, who utilize a more robust version of China's Sixth Census Yearbook. Prefecture-level GDP is obtained from the yearly volumes of the China Statistical Yearbook for Regional Economy, compiled by the Department of Comprehensive Statistics and the Department of Rural Survey of the National Bureau of Statistics for 2011-2013 (ma_china_2013). Data for 2014-2016 combines annual provincial prefecture-level GDP reports to form a comprehensive dataset, with provincial websites and other annual reports used to fill in any missing data. When determining the number of corruption indictments in a prefecture in each month, for provincial level officials, I distribute the effect across all prefectures in a province; however, only binary measures of corruption indictment are used in computing the below results.
To examine the relationship between corruption indictments and the share of listings in a prefecture, I first estimated a set of two-way fixed effects regressions but ultimately found that the assumptions are not met. Appendix (ref) provides full details and regression results, but in essence, linear fixed effects models require two causal identification assumptions: first, that past outcomes do not impact the current treatment, and second, that past treatments do not directly influence the current outcome (imai_when_2019).
In the case of the Chinese anticorruption campaign, both of these assumptions are violated as there is likely strong feedback between the treatment (the number of corruption indictments) and the outcome (the share of listings). Further, I expect that there are some time-varying confounders like gross regional product (GRP), which may make a unit more likely to be treated\textemdash for instance, if richer areas are treated sooner. At the same time, being treated likely affects the area's GRP starting from the time of treatment. Such variables are both simultaneous confounders and intermediate variables, and including time fixed effects therefore blocks part of the causal pathway, biasing estimates.
Given the causal identification assumptions for two-way linear fixed effects are not met, I implement a marginal structural model (MSM) to investigate the causal relationship between corruption indictments and sale method. Developed by Robins (1986, 1998ab, 1999ab), \nocite{robins_association_1999} \nocite{robins_marginal_1999} \nocite{robins_correction_1998} \nocite{robins_marginal_1998} the MSM is a multi-step estimation tool that aims to estimate the causal effect of a treatment on an outcome in the presence of time-dependent covariates that may be both simultaneously confounders and intermediate variables. As implemented by Robins, the MSM relies on inverse probability of treatment weighting (IPTW): IPTW in effect creates a pseudo-population by weighting each unit by the inverse of the conditional probability of receiving the treatment that it received (hernan_causal_2020). Then, passing these weights into the final MSM regression is “conceptually identical to running an unweighted, regular regression model in the pseudopopulation in which confounders and treatments are independent of each other" (thoemmes_primer_2016, p. 42), allowing a causal effect to be estimated. When the MSM's assumptions are met, IPTW can consistently estimate the model parameters, allowing for identification of the marginal mean of potential outcomes under any treatment sequence.\footnote{In this sense, the model is “marginal" because it utilizes the marginal distribution of the treatment and “structural" because it models the probabilities of counterfactual variables, which is referred to as “structural" in the econometrics/social sciences literature (williamson_marginal_2017; robins_marginal_2000).}
In the Chinese case, as described below, the basic MSM is a poor fit, as one key assumption (sequential ignorability) is not met, and another assumption (consistency) is doubtful, given many confounders that influence treatment are difficult to capture in conventional variables. I expect that many of these are time-invarying prefecture-level confounders, and this paper's main MSM specification of focus is Blackwell and Yamauchi (2021, 2024)'s MSM with fixed effects in the IPTW model.\footnote{Note that “fixed effects" is used in the econometric sense, controlling for unobserved heterogeneity\textemdash in this case\textemdash at the unit level. Note also that details on the basic specification of the MSM can be found in Appendix (ref).} This model is ideal to apply when time-constant unmeasured confounding is likely present\textemdash if units have differing baseline probabilities of treatment due to difficult-to-measure traits/features, sequential ignorability may not be met, as is likely the case here (blackwell_adjusting_2021). As Blackwell and Yamauchi highlight, the MSM with fixed effects requires restrictions beyond the typical MSM case. They concentrate on truncated MSMs, which focus on a treatment history of fixed length rather than the entire treatment history.
In implementing the MSM, I fit the following binary pooled logistic outcome model with weights calculated via IPTW with fixed effects:
using weights $w_{ij}^*$ generated from IPTW, where logit is the natural logarithm of the odds, $log\left( \frac{p}{1-p} \right)$. Here, $ACI_{ij}$ is a binary variable that captures whether any corruption indictments (hence “ACI") were made in month $j$ for prefecture $i$. $AnyListings_{ij}$ is a binary variable representing whether the prefecture had any properties sold as listings in a given month/year $j$.\footnote{In the two-way fixed effects estimation mentioned, the continuous versions of these variables were used. Note also that tenders are excluded from this analysis, as they represent a very small proportion of the data and are only used in limited, more tightly regulated settings (cai_chinas_2013; wu_primary_2020).}
Following the literature (e.g., robins_marginal_2000, imai_robust_2015, and blackwell_framework_2013), the setup of the MSM is as follows: suppose we observe $N$ units indexed by $i = 1, 2, \dots , N$ at each of $J$ time periods. At each time period $j = 1, 2,\dots, J$, we observe the time-dependent treatment variable $T_{ij}$ and the time-varying covariates $X_{ij}$ that could be impacted by past treatments. Define treatment $T_{ij}$ to be a binary treatment variable where $T_{ij} =1 $ implies that unit $i$ is treated in period $j$. Conversely, $T_{ij} =0$ suggests that unit $i$ is not treated in period $j$. Assume that $X_{ij}$ is already realized before the treatment at time $j$ and is therefore not impacted by the treatment in period $j$, $T_{ij}$.
The observed treatment history for each unit $i$ up to time $j$ is represented by $\overline{T} _{ij} = \{T_{i1}, T_{i2}, \dots, T_{ij}\}$ while the observed time-invarying covariate history for unit $i$ up to time $j$ is captured as $\overline{X} _{ij} = \{X_{i1}, X_{i2}, \dots, X_{ij}\}$. The set of possible treatment and covariate values at time $j$ is $\overline{\mathcal{T}} _j$ and $\overline{\mathcal{X}}_j$, respectively. The outcome of interest $Y_{ij}$ is observed at the time period $j$. In the basic MSM, this outcome is impacted by the entire treatment history up until $j$, and $Y_{ij}(\overline{t}_j)$ is thus used to denote the potential value of the outcome variable for unit $i$ at the time period $j$ under the treatment history $\overline{T}_{ij} = \overline{t}_j$, where $\overline{t}_j \in \mathcal{\overline{T}}_j$.
Yet, as Blackwell and Yamauchi highlight, the MSM with fixed effects requires restrictions beyond the typical MSM case. They concentrate on truncated MSMs, which focus on a treatment history of fixed length rather than the entire treatment history. This truncated MSM consistently estimates $\mathbb{E}\{Y_{ij}(\overline{t}_{[j-k, j]})\}$ where $\overline{t}_{[j-k, j]} = \{t_{j-k},{t}_{j-(k-1)}, \dots, t_j \}$ and $k$ is a fixed number of the last $k$ periods.
For any unit $i$ and time $j$, only one of these potential outcomes can be observed, as a unit cannot follow multiple treatment paths over the same time window. As described further below, the consistency assumption is therefore used to connect the potential outcome to the observed outcome; it states, in effect, that the observed outcome and the potential outcome are the same for the observed history. In this framework, $X_{i,[j-k,j]}(\overline{t}_{[j-k-1,j-1]})$ reflects the potential values of covariates for unit $i$ at each time period $j$ given the relevant treatment history up to time $j-1$. The assumptions of the MSM with fixed effects in the IPTW are as follows.
Weights for unit $i$ under hypothetical treatment history $\overline{t}_{[j-k, j]}$ are estimated as
Note that weights are stabilized, with the numerator representing the baseline probability of receiving the treatment history, as estimated by a model with no covariates.\footnote{Note that unstabilized weights have 1 in the numerator.}
As these weights $w^*$ are unknown in an observational study, they must be estimated; following the MSM literature, this usually entails specifying a parametric model to estimate the propensity score, “the conditional probability of assignment to a particular treatment given a vector of observed covariates" (rosenbaum_central_1983, p. 41). Several types of MLE estimators can be used, and I focus on the propensity score behavior when using a pooled logistic sigmoid regression, as is standard in the literature for binary treatments (imai_robust_2015; thoemmes_primer_2016; hernan_causal_2020). I omit further technical details of this specification here but refer the reader to Appendix (ref).
In my estimation, the treatment variable $T_{ij}$ is $ACI_{ij}$, a binary indicator of whether there were any corruption indictments in the given prefecture $i$ at time (month, year) $j$. To estimate the probability of unit $i$ receiving a given treatment in a given period $j$, I estimate numerator and denominator models, per ((ref)). The numerator and denominator models are each calculated using a pooled logistic model that treats each prefecture-month as an observation, generating the weight for each unit.
Once the weights are calculated as detailed above through IPTW, treatment effects can now be estimated using an outcome model incorporating the weights. The basic outcome model detailed in equation ((ref)) is used, estimating the impact of having any corruption indictments in a prefecture in month/year $j$ on whether there are any listings in the given prefecture. In line with robins_marginal_2000, covariates are not included in this outcome model to capture the causal effect.
I highlight a few final technical details. First, the most extreme weights are removed via truncation, as is standard in the literature (cole_constructing_2008; thoemmes_primer_2016; chesnaye_introduction_2022); truncation at the $1^{\text{st}}$/$99^{\text{th}}$ percentiles is used in this analysis.\footnote{Results with aggressive truncation are largely similar and are included in Appendix (ref).} As bootstrap standard errors are generally recommended in the literature (see, for instance, thoemmes_primer_2016; cole_constructing_2008; yiu_joint_2022; robins_new_1986; robins_marginal_2000; and blackwell_framework_2013), the standard errors in this paper are bootstrapped with clustering over 500 replications (a “pairs clustered bootstrap").
Specifications with prefecture-level fixed effects (column (3)) and province-level fixed effects (column (4)) are conducted in Table (ref). In addition to these unit-level fixed effects, several time-varying covariates were experimented with, and the selected model has the best covariate balance. As such, the final model has lagged GRP and its square, as well as the lag of population. The standard mean differences before and after weighting are plotted, as shown in Figure (ref).\footnote{As highlighted in the literature (for instance, chesnaye_introduction_2022 and zhu_boosting_2015), the standardized differences should be less than 0.10 for the weighted sample for all characteristics/covariates, although 0 is the ultimate target.}
Here, weighting significantly improves the standardized mean differences, particularly in the presence of prefecture fixed effects (Panel A). Now, all covariates have mean differences below 0.1, confirming that the model is balanced with respect to observed confounders. In Panel B, the standardized mean difference is slightly above the threshold for the lag of GRP, measuring 0.1013. Further checks of covariate balance and evaluation of the role of outliers are included in Appendix (ref). The results table is below.
Column (3), with its balanced covariates, can be interpreted causally, suggesting that a prefecture having corruption indictments causes a 1.16 percentage point decrease in the probability of having any listings (95% CI: (-0.0223, -.000909)), calculated via incremental effects. Column (4)'s coefficient is statistically insignificant. If interpreted causally using incremental effects, it would imply that a prefecture having any corruption indictments leads to a 0.584 percentage point decline in the probability of having any listings, but this effect is not statistically different from zero. Province-level fixed effects in the IPTW model absorb province-level time-invariant variation to test whether prefecture-level effects persist in the presence of these additional controls. This statistically insignificant result suggests that treatment $T_{ij}$, which remains at the prefecture level, indeed has a different correlation with the province-level fixed effect than the prefecture fixed effects\textemdash that is, that $T_{ij}$ is more a correlate of the prefecture-level unobservables than the province-level unobservables.
While the coefficient of column (3) is statistically significant, a natural question is whether it is likewise economically/practically significant, and the sale timeline becomes important here. As highlighted in Section (ref), areas to be inspected by the Central Inspection team were only notified 10 days before their arrival in the province, and officials therefore (in theory) had little opportunity to change their behavior in advance. Further, the decision of whether a property is diverted to auction or listing is made quite close to the sale date: after the date for the property sale nears and the price has been calculated, the property is then passed to the local land bureau, which inspects the property, decides the auction style, and conducts the sale (cai_build_2017; cai_chinas_2013; see Sections (ref) and (ref) for further details).
As described in Section (ref), most corruption waves are 2 full months, with indictments often following in the month or two after. Under this timescale, if officials do indeed divert properties towards auctions as a result of the anticorruption campaign, such behavior may occur not only in the month of corruption indictments but in those just before and after. In essence, I expect that the true trigger of their behavioral change is the investigations themselves. I anticipate that officials divert properties to auctions to either a) avoid being detected for corruption or b) avoid the appearance of such corruption. The anticorruption campaign's true causal power lies in its investigations, and indictments are only a symptom/measure of the severity of these anticorruption investigations in each prefecture. Thus, given the amount of time between deciding what sale method to use for each property and the signing date, I expect that if there is a drop in the probability of having any listings when a prefecture is being investigated, it will appear sometime around the time of corruption indictments, not necessarily $only$ in the month(s) of the indictments.
This hypothesis was tested with several versions of the standard outcome model (equation ((ref))) wherein $AnyListings_{ij}$ is converted to leads to capture future months ($AnyListings_{i,j+1}$, $AnyListings_{i,j+2}$, $\dots$) and lags to reflect past months ($AnyListings_{i,j-1}$, $AnyListings_{i,j-2}$, $\dots$), all while $ACI_{ij}$ remains as is.\footnote{Note that changing the outcome variable like this is possible in an MSM because the weights are only calibrated with the specific treatment; any binary outcome can be estimated with this logistic specification, as long as the treatment used in IPTW is used as the treatment in the outcome model, such that the weights correctly balance covariates.} The coefficients on leads 1-3 were highly statistically significant and of a similar magnitude/direction as that in column (3)\textemdash in probability terms, no lead exceeded a decrease of 1.87 percentage points on the probability of having any listings\textemdash while lags were significant and of similar magnitude only for a one-period lag.\footnote{Given the possibility that the standard weights for $ACI_{ij}$ do not fully adjust for post-treatment confounders, I examined whether these results persist (and covariate balance is maintained) when the model is re-estimated using weights from period $j+1$ while maintaining treatment timing at $j$; this specification allows me to test whether the confounder adjustment needs to be “future-aligned" for the leads\textemdash that is, whether adjustment for confounders up to $j+1$ (rather than $j$) meaningfully alters the effect of $ACI_{ij}$ on the outcomes. I find that the result is stable, suggesting that the original weights adjusted to time $j$ already account for relevant confounders whose effects may persist into $j+1$ and that the treatment effect is robust to any minor temporal misalignment in confounder adjustment timing. } These coefficient estimates are included in Table (ref) below.
Contextually, 89.31% of prefectures in any given month have at least one listing transaction. The mean number of properties sold (of both auction and listing types) in each prefecture per month is 7, while the maximum is 240 properties. For listings alone, the mean is 5 properties per prefecture per month, and the maximum is 240. Thus, a prefecture actually moving from having any listings to no listings (as a change in $AnyListings$ from 1 to 0 would indicate) would mean that the prefecture changes the sale type of the majority of its properties\textemdash and considering the time scale, this would be quite a strong effect: for there to be a statistically significant drop in the likelihood of having any listings by the time corruption indictments officially occur, prefectures must seriously shift their behavior very rapidly right at/after the start of the local Central Inspection team investigations. Thus, not only is the overall decrease accompanying corruption indictments magnified, as there are effectively 5 months ($j-1$, $j$, $j+1, j+2,$ and $j+3$) with a statistically significant negative coefficient on $ACI$\textemdash each with approximately a 1.56 percentage point decline in the probability of having any listings, on average\textemdash but this spillover behavior means that the original coefficient estimated in equation ((ref)) may be underestimated.
Therefore, ultimately, while the 1.16 percentage point decline found in column (3) seems small, when compounded across the 5 months, this amounts to 7.78 percentage points (95% CI: (-0.1113, -0.0443)). Indeed, the cumulative effect is still relatively small, but if a prefecture does substitute all of its would-be listings for auctions, this action could have a critical impact on the distribution of developers, allowing other players to enter previously closed markets and fostering a more competitive market environment long-term.
I next discuss whether the assumptions are met and briefly highlight some further sensitivity checks conducted and their (high-level) results; full details and any relevant graphs can be found in Appendix (ref).
First, for consistency to hold, the value of $Y_{ij}$ when exposed to treatment $T_{ij}$ will be the same 1) no matter what mechanism is used to assign treatment $T_{ij}$ to unit $i$ and 2) no matter what treatments the other units receive. Both of these statements should hold for all units $i$ (rubin_comment_1986). I expect there are likely some anticipation effects wherein unit $r$ sees that unit $i$ is being treated in time $j$ and adapts its behavior, effectively anticipating, and I discuss this further in light of the sensitivity test findings highlighted below.
Positivity is met in this case because in any given period $j$, there is a nonzero probability of treatment (petersen_diagnosing_2012). In the data, all prefectures experience treatment at least once, if not more. Further, some prefectures experience treatment in multiple sequential periods, so even after being treated in $j$, there is still the possibility for treatment in period $j+1$. Conversely, no prefecture is certain to experience treatment in any period.
For sequential ignorability to hold under the MSM with fixed effects in the IPTW model, treatment should be effectively randomized with respect to future covariates and the outcome, conditional on the past and time-invariant features of unit $i$. In effect, we must examine if there is still “unmeasured confounding" after controlling for time-invariant confounding via the unit fixed effects. I expect that these fixed effects capture much (if not all) of the confounding that influences treatment\textemdash for instance, the two biggest threats to sequential ignorability, suspected initial corruption level and ties of provincial leaders to Politburo Standing Committee members\textemdash because these factors are time-invariant.
I conduct several sensitivity analyses and robustness checks. I first perform robins_association_1999's sensitivity check, as implemented by ko_estimating_2003, to investigate the sensitivity of estimates to the presence of unmeasured confounders. In essence, if sequential ignorability holds per ((ref)), we have that $\mathbb{E}\{Y_{ij}(\overline{t}_j) \ | \ \overline{X}_{ij}, \overline{T}_{i, t-1} = \overline{t}_{i,j-1}, T_{ij} \}$ = $\mathbb{E}\{Y_{ij}(\overline{t}_j) \ | \ \overline{X}_{ij}, \overline{T}_{i, t-1} = \overline{t}_{i,j-1}\}$ since sequential ignorability implies that $Y_{ij}(\overline{t}_j)$ is mean-independent of $T_{ij}$ given the past $\overline{X}_{ij}, \overline{T}_{i, t-1}$. However, if unmeasured confounders are present, this equality no longer holds. The function
will be nonzero when $t_j \neq t_j'$, where $t_j'$ is an alternate treatment (ko_estimating_2003); $q_{ij}(t_j, t_j')$ is the natural measure of the “magnitude of noncomparability with respect to the mean of" $Y_{ij}(\overline{t}_j)$ of the two groups due to unmeasured confounding (robins_association_1999, p. 168). robins_association_1999 proposes a sensitivity analysis based on interpretable parameterizations of $q$. This is often selected as $q_{ij}(t_j, t_j') = \varphi\times(t_j - t_j')$ where $t_j' = 1- t_j$, and $\varphi$ is the expected difference between $Y_{ij}(\overline{t}_j)$ given $T_{ij} = t_j$ versus $T_{ij} = t_j'$ (and conditional on $\overline{X}_{ij}, \overline{T}_{i, t-1}$). Under this definition, $\varphi = 0 $ corresponds to the assumption of no unmeasured confounders. Unmeasured confounders are marked by nonzero $\varphi$ values: if $\varphi > 0$, then on average, treatment is preferentially given to those units with higher $AnyListings$ counterfactuals $\{Y_{ij}(\overline{t}_j)\}$ (i.e., corruption indictments are given to more corrupt-appearing prefectures\textemdash that is, those where a disproportionate number of listings would occur in the absence of indictments), even after controlling for past treatment and measured covariate history. As I expect that treatment is preferentially given to those units with higher (unmeasured) suspected corruption, I focus primarily on positive values of $\varphi$ in my sensitivity analysis.
In essence, when $\varphi > 0$, the log-odds of the estimated treatment effect drop consistently, suggesting that the estimates derived under sequential ignorability as reported in column (3) are conservative: they underestimate the true effect if unmeasured confounding exists. The same is true for those estimates in column (4). A further discussion (with plots of $\varphi$) is included in Appendix (ref).
For positivity, I investigate the overlap of the propensity score distribution between the treated and untreated groups for the untruncated weights, as well as petersen_diagnosing_2012's version of the parametric bootstrap which is designed to detect positivity violations. I also check the effective sample size to ensure that the weights are not dominated by a few extreme values; in all three cases, I do not find any evidence of positivity violations.
Beyond evaluating propensity score overlap, ensuring covariate balance, and checking the ESS, the literature offers no further consistency-focused sensitivity analyses that can be feasibly implemented here. Thus, while the previous sensitivity checks and statistics did not elucidate any blatant consistency violations, I suspect that consistency may nevertheless be violated and discuss the implications of this on the results. If there is in fact spillover and other prefectures witnessing the anticorruption campaign preemptively reduce their corruption\textemdash and the probability of having $AnyListings$ in turn declines\textemdash then this behavior biases the magnitude of the coefficient of interest towards zero. Then, in the presence of a true control group (i.e., where there is no anticipation), the magnitude of the coefficient would be larger and maintain its negative sign, indicating a stronger negative causal effect. Thus, even if consistency is violated by spillover, the presence of the statistically significant negative coefficient on $AnyListings_{ij}$ in column (3) suggests that the effect would remain if consistency were fully met\textemdash and the true coefficient would be more negative.
As the MSM also offers insight into behavior resulting from a certain sequence of treatments, I estimate a series of regressions to discern the impact of having sequential periods of corruption indictments on the likelihood of having any listings.
I begin with equation ((ref)), which regresses $AnyListings_{ij}$ against not only $ACI_{ij}$, but also against a one period lag, $ACI_{i,j-1}$, as specified:
This equation allows me to estimate the effect of treating two periods in sequence on $AnyListings_{ij}$, and these results are shown in column (2) of Table (ref). I likewise estimate regressions including $ACI_{ij}$ and two lags ($ACI_{i,j-1}$ and $ACI_{i,j-2}$) in column (3), and three lags ($ACI_{i,j-1}$, $ ACI_{i,j-2},$ and $ACI_{i,j-3}$) in column (4). Regressing all three of these unique specifications allows me to compare coefficients on each lag across the results to understand the stability of the estimates. Table (ref) lists the number of “runs" and observations that experience consecutive treatment. A “run" is an incidence of consecutive treatment, so for example, per the table, there are 352 incidences of a prefecture being treated in exactly two consecutive periods\textemdash and this is comprised of 712 individual monthly observations (as each two-period run yields two observations).
I also estimate ((ref)), wherein the variable of interest in each time $j$ is in effect the number of periods (up to $j$) with nonzero corruption indictments for a given prefecture $i$, as written below:
This means, for instance, that if 5 months had nonzero corruption indictments in periods 1 through $j$, then $\sum_{s =1}^jACI_{is} = 5$. Summary statistics on the frequency of cumulative treatment are included in Table (ref) as well. While prior specifications such as ((ref)) offered insight into the impact of certain treatment sequences on $AnyListings_{ij}$, this one investigates the impact of the total number of treated periods regardless of sequence; the results are shown in column (5) of Table (ref).
As Table (ref) illustrates, the simple specification of column (1) camouflages a more nuanced effect that is apparent when sequential treatments are examined. Specifically, treatments occurring in sequential periods magnify the drop in the likelihood of having any listings: when 4 periods ($j-3$, $j-2$, $j-1$, and $j$) are treated in sequence, the first period $j-3$ again has the most negative coefficient; there are then two slightly smaller but statistically significant negative coefficients for the second and third periods of treatment ($j-2$, $j-1$), and finally, for the last period, a negative but statistically significant coefficient. These specifications thus illustrate that corruption indictments in a prior period (like $j-3$, $j-2$, or $j-1$) have a stronger negative impact on current listings than corruption indictments in the same period. This result, like that in Table (ref), is likely related to the time difference between officials deciding a property's sale method and the property actually being sold, as discussed in Section (ref). In effect, it echoes the findings of Table (ref)\textemdash that there is often a delay between the period(s) of corruption indictments and the largest measured deterrent effect of the investigations/indictments.
In terms of magnitude, again using incremental effects, a prefecture having corruption indictments in four sequential periods (the three prior periods and the current period), per column (4), leads to a 6.75 percentage point decrease in the probability of having any listings in that current period. In column (4), each of these coefficients has a 95% confidence interval exclusive of zero; further, the coefficient on $ACI_{ij}$ is roughly similar in magnitude across specifications, dropping slightly in column (2) before rising again in columns (3) and (4).\footnote{Note that the p-value for $ACI_{ij}$ in column (2) is slightly above 0.05 and is thus not statistically significant.}
Perhaps most interesting is these results in comparison to the coefficient in column (5), which regresses $AnyListings$ on the cumulative count of the number of periods that a unit experienced corruption indictments up to time $j$. Interestingly, this coefficient is very close to 0 with a comparatively large standard error, suggesting it is not the number of corruption indictments but the chronology of them that most impacts the presence of listings. This result suggests that either 1) corruption investigations and indictments provide such a strong deterrent to listings\textemdash as listings give the appearance of corruption, even if there is actually no corruption\textemdash that officials avoid them around the timing of investigations but return to them, when reasonable, afterwards. Alternatively, 2) if most incidences of listings are in fact due to corruption, officials return to listings in the absence of the investigations, which would indicate a weak long-term deterrent effect of corruption investigations in the land sector. Regardless of the cause, these results highlight that the impact of corruption investigations on the likelihood of having any listings is more of a short-term result than a long-term one, as echoed by specifications from Table (ref).
A set of sensitivity checks are again conducted to ensure that the results can be interpreted causally. The results are conceptually similar to the previous outcome specifications with prefecture-level fixed effects in the IPTW model (equation ((ref)), for instance). As before, any violations of positivity, sequential ignorability, or the spillover dimension of consistency would bias the estimates towards zero, suggesting the estimated coefficients in column (4) are lower bounds for the true effect.\footnote{Appendix (ref) includes the full sensitivity checks and their results. Results for the multiple treatments in the outcome model with province-level fixed effects can be found in Appendix (ref).}
In order to better understand how corruption impacts price in land sale, I also run two additional versions of the outcome model, as detailed below:
In this specification, the outcome is the average price per square meter for (residential real estate) land sold in prefecture $i$ at time $j$. I also estimate a version of the above specification that uses $\text{log(}MedianPrice)_{ij}$ as the outcome, instead of the average price, but is otherwise identical. Both specifications use the balanced and stabilized weights utilized in Tables (ref) and (ref), as the treatment remains the same.\footnote{Note also that I use the log transformation of the outcome because there is a great disparity in prices per square meter: prices per square meter in highly sought-after areas like Beijing and Shanghai have average prices per square meter several times that of more rural prefectures. } The results, using both prefecture-level and province-level fixed effects in the IPTW model, are shown below in Table (ref).
As is apparent above, a statistically significant positive coefficient persists across both prefecture-level and province-level fixed effects in the IPTW model, for both the logarithm of the mean and median price per square meter. Column (1) yields that having corruption indictments in a prefecture in a given month/year causes, on average, a 6.78% increase (exp$(0.0656)-1$) in the mean price per square meter. Similarly, in terms of the median, column (3) suggests that having corruption indictments in a given month causes a 7.61% increase (exp$(0.0733)-1$) in the median sale price per square meter for land sold in that prefecture. Columns (2) and (4) yield very similar effects, and given the covariate balance is only borderline met for province-level fixed effects in the IPTW, I focus primarily on the results from the prefecture-level fixed effects.
The median price per square meter is around 1,400 yuan (US\$212). The mean, however, is much higher given the significant amount of stratification in underlying land demand/value: 2010-2016 was driven by the rapid urbanization of previously underdeveloped areas (such as Tier 3 and 4 cities), whose land prices per square meter were often extremely low. At the same time, land prices per square meter in places like Shanghai, Beijing, and Tianjin could be hundreds of times higher than those of more rural areas. Thus, while the mean is 2,200 yuan per square meter (US\$350), this camouflages a significant amount of underlying heterogeneity. The highest mean price per square meter sold, for instance, was in Shenzhen in June 2016 at 162,309.8 yuan per square meter (US\$24,655).\footnote{Note that while this ratio may seem extremely high, I checked the original data and verified its correctness. Given the extremely high demand in Shenzhen at the time, these were highly coveted properties in prime locations, and the sale prices were extremely high.}
Property sizes tend to be tens of thousands of square meters, if not more, so for the upper echelon of properties, a 6-7% increase in price per square meter is extremely significant. Even in more rural areas, an increase of 6-7% in the cost per square meter can cost developers hundreds of thousands to millions of additional yuan. These specifications thus suggest a non-negligible increase in the median and mean price per square meter when corruption indictments occur.\footnote{Given the ambiguity in the timing of indictments described in Section (ref), I also sought to investigate whether there is an increase in the logarithm of the average price in neighboring time periods. I sought to test this hypothesis with several versions of the outcome model (equation ((ref))) wherein $AvgPrice_{ij}$ is converted to leads to capture future months ($AvgPrice_{i,j+1}$, $AvgPrice_{i,j+2}$, $\dots$) and lags to reflect past months ($AvgPrice_{i,j-1}$, $AvgPrice_{i,j-2}$, $\dots$), all while $ACI_{ij}$ remains as is. To do this analysis, however, I need to ensure that the results persist when the model is re-estimated using weights from period $j+1$ while maintaining treatment timing at $j$. This examines whether the adjustment for confounders up to $j+1$ (rather than $j$) meaningfully alters the effect of $ACI_{ij}$ on the outcomes. I find coefficient instability across specifications, likely catalyzed by potential mediators (like sale method) that I do not control for. Instead, it suggests that time-varying confounders between $j+1$ and $j$\textemdash which are not fully captured by my controls of GRP and population\textemdash meaningfully impact both corruption investigations and price movements. Since future-aligned weights are often problematic because they adjust for post-treatment variables, I focus on the original specification while acknowledging that monthly spillover is possible but uncertain.} Note also that part of this positive effect is likely due to a slightly higher proportion of auctions that accompany corruption indictments, as auctions are associated with higher prices in the literature. This coefficient is therefore more of a total effect (including this mediator of sale method) than a direct effect of only corruption indictments on the average sale price per square meter.\footnote{Another pathway through which corruption indictments could impact price, for example, is the floor area ratio (FAR). In the presence of corruption, the FAR of a property could be set low at the listing stage, deterring other possible bidders. Then, sometime after sale, the developer may bribe an official to raise the FAR, allowing the developer to build more square footage on the land. In the presence of the anticorruption campaign, officials may reject bribes, setting the FAR higher at the time of sale rather than adjusting it later. In doing so, the sale price would be higher.}
Sensitivity checks are conducted (Appendix (ref)). While the checks reveal the results are sensitive to violations of sequential ignorability, the lack of obvious (uncontrolled for) time-varying confounders ameliorates this concern. The tests broadly suggest that the specifications are well-fit and do not have glaring violations of positivity. Again, the presence of anticipation threatens consistency, but further analysis (via other identification methods) would be needed to confirm whether this meaningfully changes the direction of the coefficients.
These results have important implications on the supply and demand dynamics underpinning residential real estate in a market highly susceptible to corruption\textemdash not only does this analysis show that the anticorruption campaign deters listings, but that prefectures investigated for corruption see a short-term increase in prices.
Analyzed in tandem, these results ultimately suggest two potential diverging conclusions about corruption in the Chinese land market. The first possibility is that the incentive to engage in corruption in the land market is so high that in the absence of an immediate credible threat of indictment, corrupt behavior persists, with land being diverted towards listings. In this lens, prices rise towards the level that the market demands when corruption is deterred. Ultimately, though, the anticorruption campaign fails to deter corruption beyond the period immediately surrounding investigation.
The other pathway is that the anticorruption campaign creates so much fear of indictment that officials substitute away from actions that even have the appearance of corruption\textemdash such as selling properties via listing. The departure of the Central Inspection team, then, allows normal behavior to return. In this view, it is not certain whether listings actually foster corruption, but they are definitely associated with the appearance of corruption. Prices rise when corruption indictments occur\textemdash but this is counter to government desires to lower prices/price growth and stem the formation of a property bubble (as discussed in Section (ref)). In this world, the anticorruption campaign inadvertently impedes the government's goal of lowering land sale price growth, and the departure of the campaign means that the sale method can return to its equilibrium.
At the nexus of these options is the question\textemdash does the campaign feed off of corruption as it is perceived or as it actually exists? I expect that the reality is a combination of both cases: in an environment with investigators dispatched to a province for a short period of time, on the lookout for any whiff of corruption, officials divert towards auctions to avoid trouble\textemdash but at the same time, it is more likely that those who do divert have something to hide. After all, a marked body of literature suggests that listings are hotbeds of corruption, so there are almost certainly some properties being (corruptly) diverted to listings pre-campaign.
Simultaneously, anticorruption indictments cause higher prices, which goes directly in the face of the government's goal of moderating land sale prices.\footnote{I expect that part of this effect is driven by the shift towards auctions, which have a higher sale price on average. Yet, it cannot be determined whether prices increase beyond the level that the increase in competition causes.} If anything, one would expect the proportion of listings to rise slightly throughout this time period as officials worked to moderate land sale prices, which could sometimes skyrocket in auctions. Thus, in the absence of the anticorruption campaign, corruptly diverting “hot" properties toward listings would be almost entirely camouflaged and would likely spike further. In this setting, the shift away from listings\textemdash especially apparent in the statistically significant binary case of $AnyListings$ and its leads/lags\textemdash suggests an extremely strong (temporary) shift in behavior, almost an over-reaction.
I thus expect that the anticorruption campaign does deter actual corrupt behavior of having listings on favorable properties, but also impacts behavior for properties on the margin (i.e., those that could be sold as either auctions or listings). After all, those who have the best idea about whether the sale method selected for a certain property is defensible are those in the local land bureau who are intimately familiar with the government's motivations, aims, and the property sale landscape. The results indicate that these officials do change their sale method selection around the time of the campaign, and it is likely because a certain subset of properties could be auctions\textemdash or should reasonably be auctions. At the end of the day, each official conducts a utility calculation, weighting the desire to protect oneself with external factors and possible kickbacks, and this calculation may not include whatever broader aims the local government may have about keeping price growth in check.
The statistically significant negative effect on $AnyListings$, however, does not persist past three leads, nor is the cumulative amount of periods with at least one corruption indictment significant. The shift towards auctions is thus short term. Yet, in the periods after corruption indictments, there is no evidence of an increase in the probability of having any listings, as would likely be the case in the absence of the campaign (due to the government's desire to stem price growth). Thus, after the investigation team departs from a province, there is likely a simultaneous decrease in the corrupt diversion of listings to auctions and a general shift towards listings to stem price growth\textemdash these two factors offset each other and create the null effect observed in future periods. Yet, while this is my ultimate reasoning based on the results, the fact that so many factors intersect here means that this conclusion is far from certain.
On its own, this paper's main implication is thus the clear causal effect of the anticorruption campaign on the probability of having any listings, providing strong evidence of the campaign causing a (short-term) substitution towards auctions. Future research should focus more on the relationship between corruption indictments and price, working to partial out the effect of the sale method itself, to determine whether the price post-corruption indictment is higher when controlling for sale method. If so, this would be a strong indicator that the anticorruption campaign is successful in combating corruption: even if the share of listings still rises after corruption indictments occur, a higher price would indicate that these listings are less susceptible to the kind of pervasive corruption that historically occurred.